Alberta #2

There are 3 different versions of the Alberta site that have been applied in multiproxy reconstructions: 1) Luckman et al [1997] used in Jones et al [1998]; Crowley and Lowery [2000]; Briffa [2000]; 2) Esper et al. [2002] ; 3) the version used in Osborn and Briffa [2006], presumably from Luckman and Wilson [2005] and presumably the one used in D’Arrigo et al [2006] (although details of the latter are lacking). Each version has replication issues with permutations based on data combinations and methodology variations.

A theme that’s emerging for me here is: on a macro-scale, the Hockey Team takes great comfort in what they regard as "similarity" in the hockey sticks in the spaghetti graphs. However, at the level of individual sites, it’s remarkable how little similarity there is between versions. I’ve commented on this for Polar Urals. I’ve noticed something similar for Greenland – remind me to post this up. Today I’ll nibble at the Alberta site, showing the 3 versions used in multiproxy studies and a trial emulation of the Esper et al. version. I’ll get to trial emulations of the Luckman versions on another occasion.

Figure 1 below shows the three multiproxy version in a format often used by the Hockey Team – the data has been smoothed with a gaussian 40-year filter and then scaled. As you see immediately, the two Luckman versions (the later one being labelled Osborn here since it was used in Osborn and Briffa) are fairly similar ( unsmoothed correlation is 0.72; smoothed correlation is 0.65), but the Luckman versions are quite different from the Esper version (0.26 for both smoothed and unsmoothed correlation between Esper version and later Luckman version.) The low-frequency variability in the Esper version is greater than the low-frequency variability in either Luckman version ( readers should recall that there’s been much pontificating about the causes of differing low-frequency variability with arm-waving about tropics versus extratropics, but none of the commentators seem to have bothered examining individual series in detail. Maybe the issues are different than people think.) The Luckman reconstructions are primarily based on the MXD reconstructions, Esper on the his RCS RW series.

We also see remarkable differences in the early 15th century values – these are at series lows for the Esper reconstruction and near series highs for the Luckman reconstructions. It seems to me that differences such as this should cause people to pause a little before concluding that they know final results to within 0.2 deg C. or so, as Mann claimed recently at the NAS panel. I would like it if authors reconciled site results: for example, it would be interesting to see how Esper et al [2002] reconciled their highly divergent results to those of Luckman et al 1997, at least in their Supplementary Information; same with Luckman and Wilson [2005] with respect to Esper et al. 2002.

Figure 1. Alberta ring widths from near Athabasca Glacier for Luckman et al [1997], Esper et al [2002] and as used in Osborn and Briffa [2006].

I’ve done a fair bit of work trying to emulate each of the versions, and each emulation attempt leads into many by-ways. Today, I’ll report on the one where the data was most cleanly available (at least as of 7 days ago) – Esper et al. [2002]. Figure 2 below shows the Esper version (colored blue for consistency), my "emulation" of this using RCS on the data set ath.rwl provided by Science presumably from Esper; and thirdly, my emulation using RCS on all 4 Schweingruber data sets in the area (cana170w, cana171w, cana096 and cana097) – only the first two are used by Esper (but the first and third are used in L97 and all four plus others are used in LW05).

While there were important similarities, there were some important and puzzling differences. The correlation between my emulation and the archived Esper version was 0.85 (0.83 – smoothed), but the differences are striking. The Esper version does not contain the 20th century decline shown in my emulation. This difference probably relates back to Esper’s distinction between "linear" and "nonlinear" trees – a distinction that is not made in botanical texts on conifers to my knowledge. I have requested details on how this distinction was made for a very long time and it still remains as mysterious as ever. Also intriguing is the RCS result using all 4 available data sets in the area – in other cases (e.g. Mangazeja), Esper collected 4 data sets – why not here? Especially since cana096 was actually used in L97, which Esper cited.

LW05 has dated quite a few snags to the MWP which remain unarchived. Other than that, it appears to me that the 4 data sets used in the calculation are, at a minimum, a very large subset of the LW05 data and should yield an approximation to the larger LW05 data set in its later portion.

(Updated) The all-WDCP emulation shown below, based on one RCS curve for all 4 data sets, should be a reasonable approximation of a RCS RW version in Luckman and Wilson [2005] periods using one regional curve. Such an RCS curve shows the remarkable phenomenon of the site chronology declining steadily from the late 18th century. LW05 show an STD chronology, which I’ll show in a forthcoming post. As to the RCS method applied to RW data, LW05 observed:

"Significantly more low-frequency information was captured using the MXD data (See Appendix) but no significant gain was observed by using the RCS method on the RW data (analysis not shown)".

In comments below, Rob Wilson pointed out that the RCS version used in their analysis contained startification levels. Obviously such stratification will tend to move results from a bulk RCS curve towards the STD curve. Obviously, there is more low-frequency information in the “bulk” RCS curve, but this may not be so in a “stratified” RCS curve. Hopefully, we ‘ll be able to get some information on the form of stratification and see how this works.

The difference between my RCS calculation using all four WDCP data sets and the Esper archived version using two archived data sets is also dramatic. Again I’m not saying that anything is right or wrong. Also startification will tend to reduce differenecs. At the NAS panel, Mann purported to be able to estimate 11th century temperature to within 0.2 deg C (a far lower confidence interval claimed in LW05 for example – see Rob Wilson comment below). It’s hard for me to see how Mann can reach such conclusions resulting from such unstable results.

Note: I have other material which I intend to post up and will post up information on the STD RW reconstruction and on regressions (I’d intended to do so anyway, see “nibble” comment above, but see Rob Wilson comment below.)

36 Comments

You need to get a grant to support this stuff. Too bad you are in a dinky country with solid PC politics instead of the burly US where it is big enough and occasionally conservative enough that you can get divergent research funded.

While you’re right, TCO, think about who might dare to support him. Obviously one of the oil companies might but the warmers have already poisoned the well there. Conservative US groups might but the same problem applies. Even if a leftist group did there might be problems with conditions which would tie up the money if he agreed to take it. About the only possiblity might be a group on the left which would award a one-time, no strings attached award. But since all such groups I can think of would not dare to do so (or wouldn’t want to), I don’t know that it’s going to happen.

Personally, I like the idea of Amazon book links, a Cafepress store of great “skeptic” good (I’d be willing maybe even to design some stuff up for it), etc. How about prints of Steve’s papers in “bound” form from Cafepress? Sure you can download them, but how about a “hardcopy” for the coffee table?

Of course, I’m sure Steve will be lambasted for trying to “profit” from his research…

What’s peculiar to my eye is that the Esper version in Figure 1 diverges from Osborn’s and L97’s chiefly between about 1100 and 1500. It almost looks like Esper’s data were inverted about “0” in that interval, relative to the other two plots.

I also don’t see what legitimate data-reduction method one can apply so that the result from the same data is approximately linear in one reconstruction — Osborn between ~950 to ~1150 — but steeply descending in another — Esper, L97 in the same region of Figure 1.

In Figure 2, your emulation does a pretty good job of matching Esper until about 1550. After that, just eye-balling the difference, it looks like Esper’s data have a periodic intensity that your emulation is missing. Could some sort of alternative scaling step account for that? What does a difference plot show?

The 20th century divergence is especially notable given the AGW controversy. I wonder how all three published reconstructions produced a positive 20th century trend, when your emulation and the full WDCP did not. Maybe that difference comes from knowing which trees are recently T-linear and which are not?

I suddenly wonder again about the circularity problem, of choosing trees with RW’s that correlate linearly with recent temperatures and then supposing that they have done that all through their growth cycle. Doing so would guarantee that the 20th century would show a rising trend, but the reconstruction could say nothing at all about the the relative temeratures of uncalibrated centuries prior.

You are very quick to blame the whole of the palaeoclimate community for sloppy practice, but I am afraid that you are guilty of rushing your “audit” and therefore muddying the story, and guilty of misinformation. Many of my colleagues tell me to ignore you, but I cannot keep quiet when your comments are based on assumptions and guesses. Your two posts on the “Alberta” site are counter productive. Lets see if we can clarify some of the more pertinent points.

Firstly, Brian and I have already promised you that at some later stage (we will both be away for the next few weeks) to help you as much as is realistically possibly. We have nothing to hide, but your public comments criticizing us and questioning our science does not develop a good foundation from which friendly discourse can result.

Secondly w.r.t “I hardly know where to start a discussion of the Alberta ring width data”
Well – with regards to the RECONSTRUCTION of Luckman and Wilson (2005) – used by Osborn and Briffa (2006) and D’Arrigo et al (2006) – the series is weighted more strongly towards maximum density data. I have told you this already and it is quite obvious if one reads the 2005 paper. This information is not buried. The same goes for Luckman et al (1997) and hence the similarity between that and the 2005 update study (your Figure 1). The data that Jan Esper used are ONLY ring-width. Again, as I have told you in earlier e-mails, maximum density and ring-width data are doing quite different things in this region of the world. However, they compliment each other very nicely when combined using multiple regression to develop a reconstruction. More discussion on this is detailed in an earlier paper:http://freespace.virgin.net/rob.dendro/pdf/Wilson%20and%20Luckman%202003.pdf

Thirdly, you are also, yourself, guilty of abusing horribly the RCS method. In only rare (and these are debatable) situations can one RCS curve be used to derive a valid RCS chronology for a site/regional composition. Even with the much larger RW data-set that we had for the 2005 study, I was still not able to derive a workable RCS chronology that was ‘significantly’ DIFFERENT to the so called standard (STD) version that we used – i.e. there was no GAIN from using RCS. Hence following the principle of “Occam’s Razor”, I used the simpler less noisy/biased approach. In your Figure 2, you should at least show our STD ring-width chronology (archived at the WDC). Such a chronology is possibly restricted in the frequency domain due to detrending, but will not have the biases that can be introduced from the misuse of the RCS method – as you have done.

Fourthly, at no point do we ” ascribe confidence within 0.2 deg C”. Please look at Table 3 in LW2005. The standard error of the regression estimate is 0.62 – that equates to a 95% confidence of over 1.0 degree Celsius. Similar results are detailed in the Wilson and Luckman 2003 study using different data from a neighboring region in Canada. These error bars (calculated over the calibration period and not the verification period) could be further inflated – e.g. they do not include the added uncertainty of the regression coefficients themselves, and also the change in signal strength of the tree-ring chronologies through time (see LW2005 Figure 2). I am not sure where you got your 0.2 value from.

Finally, I struggle to see your motives Steve. Science is not only emulation and replication of results – it strives also to move forward and enhance understanding. It is time for you to climb down from your fence and do something positive. For example, it is time for you to do your own reconstruction (local or large scale). If you think the data are not good enough, then write a paper stating why you think so and then send it out for review. Or why not explore your ‘mixed effect model’ ideas – that could be a real boost to dendrochronology.

There is no scientific gain from debunking science on a blog. It is meaningless. If you have found realistic significant flaws, then they should be published in the relevant journals. I challenge you to do this if you truly think there is a problem. You have already done this before and probably, in that case, got more mileage than you did from your blog. At the moment, you are hiding behind a curtain of criticism using a platform where you can write anything. Who is auditing you? Many of your blog readers appear to believe you blindly. That is a dangerous situation when your information may not always be correct. Criticism is easy. It is now time to do something positive for palaeoclimatology Steve. If you cannot, then perhaps it is time to leave the field open for those who care about the science for science’s sake.

Rob, I do agree your reasoning to a certain extent. I hope that Steve doesn’t fall in the trap to critisize everything that is published by any scientist in the field remotely connected to climate research. Steve has built up a lot of credit by establishing the not so scientific methods used to produce hockeysticks, and the lack of archiving relevant data by many scientists, but I have the impression that the overall tone on this blog is going too negative, which eats away its credibility…

On the other hand, I have the impression that there are too many problems with dendroclimatology to make it a reliable base for temperature reconstructions.
Not only growth season temperature is not the only influence on ring width and density. Precipitation (which is not always synchrone with temperature) is at least as important and other factors like fertilisation (CO2, nitrogen, minerals), especially on poor soils, may be even more important at certain sites. And not to be forgotten the influence of direct/indirect sunlight (cloud cover, dust, volcanoes) on growth. Further, many species show an upside down U-shaped temperature curve, where temperatures higher and lower than the “optimum” temperature show lower growth. And the negative temperature-growth relation at the large majority of the sites since 1950 (or later) of still unknown origin is not very reassuring either (for dendro reconstructions and/or instrumental data…). Thus how can dendro reconstructions make a differentiation between all the influences, if many of the relevant confounding parameters of the past are not known to any accuracy?

Maybe there is some hope from other measurements (d18O, dD,…) on (sub-fossil) wood. Is there already something known from these alternatives?

I also agree that Steve should get more published work out. Had the bizarre experience of having Steve justify sending a paper to Nature that belonged with a specialty journal (saying it was no waste of time to “expose the position”–HUH!?) and then later have Ross complain about how publication is an issue since they wasted time getting rejected by Nature.

That said, I think he pushes the thinking in an excellent manner on this blog. Also, it is clear at times that he is doing individual analyses and trying things out. He will also engage on specifics and let himself be proven right/wrong.

Rob…I absolutely think you should engage with Steve. He will push you to better results much more than your other colleagues.

In a perverse way…one can take your criticism of the blog-level analysis as a positive. Because his work is of sufficient caliber that it really needs to be cleaned up and submitted in the journals (and exposed to counter-criticism and improvement by others, etc.)

#7 This looks like a very good post from someone in the established dendrochronology community. I think the reason that Steve has taken the tack that he has is that he found an incredible amount of opposition and obstruction when he began to investigate these issues. It is easy to say that he should publish his critiques in the standard journals rather than on a blog. It is much, much harder, however, to publish an article that questions and criticises the existing framework of analysis in a subject than one that makes another marginal contribution within the paradigm.

As one can discern by reading this blog (although there is admittedly a lot of chaff along with the wheat), Steve has also offered on occasion to work with established scholars in the field to come up with a joint article that lays out exactly what they can and cannot agree on and dicsusses the data and methodology in a frank way.

You seem like a very reasonable fellow. Why don’t you and Steve get together and work on a joint article on the Alberta sites discussing all the data sets and publications based on those data sets and the different methodologies people have used to analyse those data sets. You could use it as an example of how this work ought to be done in the future, with full public disclosure of data and methods.

There is no scientific gain from debunking science on a blog. It is meaningless. If you have found realistic significant flaws, then they should be published in the relevant journals. I challenge you to do this if you truly think there is a problem. You have already done this before and probably, in that case, got more mileage than you did from your blog. At the moment, you are hiding behind a curtain of criticism using a platform where you can write anything. Who is auditing you? Many of your blog readers appear to believe you blindly. That is a dangerous situation when your information may not always be correct. Criticism is easy. It is now time to do something positive for palaeoclimatology Steve. If you cannot, then perhaps it is time to leave the field open for those who care about the science for science’s sake.

I have to strongly disagree with this sentiment. The problem is not simply that some scientists appear to be misusing statistical analysis, but more general: that the journals themselves are not the independent arbiters and gatekeepers of good scientific practice but are actively involved in promoting those analsyses and suppressing work which demonstrates the fallacies of the approaches used.

Criticism is easy. Informed criticism is not. I think Steve has demonstrated that he does care about the science. To not expose the shoddy practices of a few would be to effectively tar all climate scientists with the same brush.

#7: I am really glad to see a dendrochronologist speak out here. Please keep it up; we certainly need the expertise to better understand your positions. BTW, can you provide some basic references to document the effects of temperature on tree growth?

Rob, I also want to thank you for the informative comments. It’s true that this blog is rather informal in tone, and many on both sides of the debate get carried away at times. One of the criticisms heard here from time to time is that “real” climate scientists are always subjected to abuse if they bother to post. The reactions to your comments disprove this (at least so far). I’m neither sufficiently qualified nor informed to fully evaluate the technical points you raise, but my impression of Steve is that he will constructively engage them and, if shown wrong, will acknowledge this.

I will, however, say that I respectfully disagree with your position regarding Steve’s blog. I too would like to see Steve publish more work, and I fully understand your position that most scientists see such peer-reviewed publications as the foundation of reasoned scientific debate (Steve’s issues with same notwithstanding). But in my opinion, forums such as this represent the best chance for interested laymen to become acquainted with and informed on the topic. Plowing through the scientific literature is beyond the time constraints of ordinary indivdiduals, albeit we still wish to have informed opinions. There is a real need for media that delve beyond soundbites to present real data and qualified opinions. Real Climate, for example, presents itself as exactly such a mechanism. Their blog contributes little or nothing to the body of climate science. Rather, it is an attempt to present climate science to the public at large. Steve’s blog is little different in that regard, although in my opinion it is vastly superior in encouraging actual debate on the topic and in tolerating a wide range of views.

What bothers people like me is the reluctance of the paleoclimate community in general (and the authors of RC in particular) to truly engage in the debate. Steve raises point after point, issue after issue, in excruciating detail, that go almost entirely unanswered. If the community does not engage him in this (or similar) forums, it certainly leaves the impression that they have no answer to his points.

The work of scientists like you is important to all of us. It informs the policy debate (whether you want it to or not). As such, it’s a matter of significant public interest. And while you don’t have a formal “duty” to inform the public, I would suggest that participants in any scientific endeavor (such as climate science) which carries potential for profound impacts on people’s lives have a degree of moral obligation to address reasonable and informed criticisms of their work. Whether Steve’s work is published or not, his criticisms are (for the most part) both reasonable and informed. Steve is performing a valuable service by subjecting such work to critical scrutiny, and exposing what appear to be serious flaws in much of the recent body of work, both in terms of content and process.

You say that many of your colleagues urge you to ignore Steve. I’m glad you’ve chosen to ignore this advice, at least in this instance. I hope to see more from you, and from your colleagues as well. You may get “flamed” occasionally (those people you can ignore!), but for the most part I’m confident that you will find your reception here respectful even when contrary opinions are expressed. Constructive disagreement is a powerful thing. Perhaps I’m simply naively optimistic, but I continue to believe that those of us with open minds will filter out the chaff and be swayed by the best argument.

I have, on many occasions, mentioned my respect for Rob Wilson and do so again. In my posts, I specifically stated that I had received cordial replies from both Brian Luckman and Rob, who were unable to assist with data issues at present due to other commitments. I realize that they can’t drop everything to assist me in an inquiry and did not criticize them for this.

My post on the Alberta series was primarily in the context of Esper et al 2002. I don’t think that it was particularly critical of the two Luckman publications other than the lack of archiving. However, I see that there are a couple of comments that have been mis-construed as being critical and I will modify them. I will change the phrase “I hardly know where to start a discussion of the Alberta ring width data”. My comment was more related to writing issues, but has come across (and I see why) as very negative comment, which wasn’t what I intended here. The writing issues that I was thinking about were the various provenance, emulation, regression issues and I couldn’t figure out how to organize my comments. I’ll change this phrase to reflect what I meant more accurately and apologize for any perceived insult. A second comment was the 0.2 deg C. Regular readers of this blog realize that this was made in the context of Mann at the NAS Panel, but this is obviously not clear to readers stepping in and out. I will modify this. (Update: I made some other clarifications and edits when I started to clarify points in response to Rob’s remarks. )

As to the comments being "rushed", readers of the blog realize that I’ve been trying for many months to get data from Esper, who refused to acknowledge polite inquiries. I received little cooperation from Science in this respect at first and only got anywhere after making a public stink about it. The issue is not archiving data so that I can access it, but it’s archiving the data (and methods if necessary) so that they are publicly accessible and so that Science complies with its own policies. When I finally got some data, I was interested in what it looked like. The quasi-litigation process with Esper has hardly been rushed. I’d spent a lot of time getting access to Esper’s data and I was interested in seeing how it compared to other versions from various sites.

Another point of context that may not be apparent to Rob. Hanson of Science twitted me saying that, as far as he could tell, Esper data that he’d looked at was already at WDCP – and that I was a fool for not knowing this. My first post was on whether someone could tell from Esper’s references that he used a combination of cana170w and cana171w. I don’t see how anyone could.

Rob said:

Firstly, Brian and I have already promised you that at some later stage (we will both be away for the next few weeks) to help you as much as is realistically possibly. We have nothing to hide, but your public comments criticizing us and questioning our science does not develop a good foundation from which friendly discourse can result.

Re-reading the two posts, I think that they are critical of Esper et al [2002] rather than Luckman, other than on the issue of archiving. In fact, I made a number of quotes from Luckman, which indicate (to me) an attempt to report carefully. Rob, I’ve edited a couple of comments and if there are comments that you disagree with specifically, you can communicate with me online or offline and I’ll see what I can do.

Rob said:

Well – with regards to the RECONSTRUCTION of Luckman and Wilson (2005) – used by Osborn and Briffa (2006) and D’Arrigo et al (2006) – the series is weighted more strongly towards maximum density data. I have told you this already and it is quite obvious if one reads the 2005 paper. This information is not buried. The same goes for Luckman et al (1997) and hence the similarity between that and the 2005 update study (your Figure 1). The data that Jan Esper used are ONLY ring-width.

I know that the MXD is more highly weighted in your paper. I’ve got some other notes in progress and was getting to that. What intrigued me here was the difference between the RW and MXD results.

Rob said:

Again, as I have told you in earlier e-mails, maximum density and ring-width data are doing quite different things in this region of the world. However, they compliment each other very nicely when combined using multiple regression to develop a reconstruction. More discussion on this is detailed in an earlier paper: http://freespace.virgin.net/rob.dendro/pdf/Wilson%20and%20Luckman%202003.pdf

As you say, MXD and RW are doing quite different things in this part of the world and there are differences between the Esper version and the other versions. It’s something that is worth pointing out and I don’t see what’s wrong with pointing it out. I think that the issue of whether RW and MXD "complement" each other in a multiple regression is very much an open question. I was in the process of working up these notes. I’m not at all convinced that multiple inverse regression is an appropriate technique for what you’re trying to do. I’m working up some notes and, if you’re interested, would welcome your comments on them.

Rob said:

Thirdly, you are also, yourself, guilty of abusing horribly the RCS method. In only rare (and these are debatable) situations can one RCS curve be used to derive a valid RCS chronology for a site/regional composition. Even with the much larger RW data-set that we had for the 2005 study, I was still not able to derive a workable RCS chronology that was ‘significantly’ DIFFERENT to the so called standard (STD) version that we used – i.e. there was no GAIN from using RCS. Hence following the principle of “Occam’s Razor”, I used the simpler less noisy/biased approach. In your Figure 2, you should at least show our STD ring-width chronology (archived at the WDC). Such a chronology is possibly restricted in the frequency domain due to detrending, but will not have the biases that can be introduced from the misuse of the RCS method – as you have done.

These were interim blog postings not 20 page papers and I intend to post up STD information. As to my "horrible" abuse of the RCS method, I’ve attempted for nearly a year to obtain an operational definition of linear versus nonlinear trees as used in Esper and have received no response from him or Science. Stratification procedures need to be articulated. I’ve mentioned to Rob in private emails that I’ve done work on reconciling "Standard" and "RCS" methods with linear mixed effects models. None of the articles in question provide operational definitions of stratifications used between RCS and STD. As a first cut at replicating Esper, I don’t see anything wrong with starting with a bulk RCS curve and then see the effect of stratifications (right up to the STD by-tree stratification.) It’s hardly a "horrible abuse".

Rob said:

Fourthly, at no point do we ” ascribe confidence within 0.2 deg C”. Please look at Table 3 in LW2005. The standard error of the regression estimate is 0.62 – that equates to a 95% confidence of over 1.0 degree Celsius. Similar results are detailed in the Wilson and Luckman 2003 study using different data from a neighboring region in Canada. These error bars (calculated over the calibration period and not the verification period) could be further inflated – e.g. they do not include the added uncertainty of the regression coefficients themselves, and also the change in signal strength of the tree-ring chronologies through time (see LW2005 Figure 2). I am not sure where you got your 0.2 value from.

As another blogger pointed out, the 0.2 deg came from Mann at the NAS Panel. I’ll edit and make this clear as it was in no way a criticism of Rob and Luckman.

Rob said:

Finally, I struggle to see your motives Steve. Science is not only emulation and replication of results – it strives also to move forward and enhance understanding. It is time for you to climb down from your fence and do something positive. For example, it is time for you to do your own reconstruction (local or large scale). If you think the data are not good enough, then write a paper stating why you think so and then send it out for review. Or why not explore your “mixed effect model’ ideas – that could be a real boost to dendrochronology.

I don’t see how I can attempt to do a positive reconstruction until I’ve been able to fully replicate prior work in the area. It is unfortunate that this is so difficult to do. Also it’s impossible when people don’t archive their data. In one of the posts that you criticize, I do no more than discuss candidate data sets – how is this not an effort to improve understanding?

Rob said:

There is no scientific gain from debunking science on a blog. It is meaningless. If you have found realistic significant flaws, then they should be published in the relevant journals. I challenge you to do this if you truly think there is a problem. You have already done this before and probably, in that case, got more mileage than you did from your blog.

I don’t know why you describe what I do as "debunking science". If I am able to debunk something, then it was never "science" in the first place. I started this blog as a form of self-protection. I was being unfairly trashed at realclimate. I didn’t notice a lot of people sticking up for me over there. Of course, if they did, it would be censored, but that’s a different story. Other people have told me to submit some more articles to journals and I probably should. A lot of what I do is replication. There are a couple of economics journals that take replication articles, but it’s an odd category for climate articles.

Rob said:

At the moment, you are hiding behind a curtain of criticism using a platform where you can write anything. Who is auditing you? Many of your blog readers appear to believe you blindly. That is a dangerous situation when your information may not always be correct.

I would hardly say that I’m "hiding" here. Everything’s out in the open. If someone disagrees with anything that I say, they can write whatever they want on the comments section. And anyone who want to have a masthead post, including yourself, is welcome to do so. Having said that, the audience here has grown over time. I do try to limit myself to comments that I can document, but there are always temptations to over-reach and I try to correct this as quickly as possible.

BTW if you transpose your observations to the peer-reviewed journals, where the journals have editors committed to certain policies or POVs, I’m not sure that the same statements don’t apply there. Consider Wahl and Ammann. They put statements into the "peer-reviewed literature" which are untrue. This then gets relied on and is a far more dangerous situation. I’m amazed at the amount of uncritical reliance on material that has had minimal due diligence on it.

BTW, I’m reading your paper right now. It really is an effort to read it all the way through…but I’m already detecting what I think are lapses:

-qualitative statements on methodolgy, not backed up with numbers
-what the hell is “capturing more information”?
-what is a NH proxy? I don’t think there is such a thing. There are NH reconstructions. But proxies? Also, if you want to say that your site is useful for understanding NH or regional variation, then why NOT LOOK AT THE INSTRUMENTAL RECORD. Just see if your location tends to follow variation of the hemisphere temp, for INSTRUMENTAL DATA!
-some circularity. It’s a good record because it matches other records. Or we used a method that tends to match other results. If you do that, then you have to presuppose that the initial work was correct and you remove any chance of invalidating other work. In other words, what is the use of the new work?

BTW, why aren’t your data archived (the snags)? Please don’t tell me, that “everyone does this”. It’s unsat. Look at crystallography databases for good practice. If you decide to persist in bad practice, you deserve to have your work looked at with skepticism.

There is no scientific gain from debunking science on a blog. It is meaningless. If you have found realistic significant flaws, then they should be published in the relevant journals.

Unfortunately history shows this idealistic view is flawed. The late Thomas Gold talked about the herd mentality and its effects on peer review. Once an idea is established within the herd it takes considerable effort to dislodge it. While getting published is relatively easy if one stays within the norms of the herd, ideas outside the norm will often face considerably more opposition if not downright censorship. That is not to say that peer review should be abandoned, as it clearly serves a useful function. Rather, one has to realize that peer review is not perfect and can at times censor legitimate ideas. To overcome this censorship one may need to resort to other methods to get their views heard. These other methods are needed to gain enough momentum in the science community to overcome the “herd instinct”. One recent example would be the work of Warren and Marshall on ulcers.

There is no doubt that Marshall, 46, has been one hell of a salesman. That helps explain why he is so well known for a discovery which stemmed from the observations of a colleague, Dr Robin Warren. In the early 1980s, Warren, a pathologist at Royal Perth Hospital, had become resigned to unkind jokes from his peers about his theory that an unusual bug he was seeing down his microscope had some role in causing stomach inflammation. No-one had taken much notice because it was such an outlandish notion.

The Nobel prize press release states:

This year’s Nobel Prize in Physiology or Medicine goes to Barry Marshall and Robin Warren, who with tenacity and a prepared mind challenged prevailing dogmas.

The obstacles that Marshal and Warren faced appear similar to those that Steve and Ross have encountered.

Strikingly, the hypothesis that the gastric spiral bacteria caused ulcers had a much more positive initial reception from medical microbiologists than from gastroenterologists, who had pre-existing ideas about acidity as the major causal factor in ulcers. Marshall and Warren’s (1984) report of their 1982 study was not immediately accepted by the editors of The Lancet, who had received negative referee reports. But as the result of the 1983 meeting in Brussels a number of microbiologists such as Martin Blaser began finding the bacteria in patients with gastritis and ulcers. The growing recognition of the importance of Marshall and Warren’s research made gastroenterologists take it more seriously. Using a football analogy, we might describe the acceptance of the bacterial theory ulcers as a kind of “epistemic end run”: a direct assault on gastroenterology was unsuccessful because of entrenched ideas in that field, but an indirect pursuit of the new ideas was possible via microbiology.

IMO, this blog is Steve’s “end run” on the accepted beliefs of the herd. M&M’s “indirect pursuit”, their “end run”, is through the field of statistics. The blog gives M&M a forum to present their views, to a much wider audience, and in far more detail then is practical in the traditional peer reviewed journals. There are no 500 or 300 word limits here. I would suggest, that without this blog, M&M’s original critique would have, over time, drifted into obscurity. I would also suggest that the well reasoned arguments presented here are gaining traction in the scientific community. In effect, the blog is instrumental in changing the direction of the herd and the willingness of the herd to accept publication of their work. This blog is not a substitute for peer review, it is a stepping stone to overcome the inherent flaws, or as Thomas Gold would say, the “herd instinct” of peer review.

Unfortunately history shows this idealistic view is flawed. The late Thomas Gold talked about the herd mentality and its effects on peer review. Once an idea is established within the herd it takes considerable effort to dislodge it.

Too bad you’re not gonna get your wish.

The folk who do things for a living share their results in the journals. That’s the standard. That’s where people who do things for a living share their results. It’s too bad you don’t like their results.

I wonder if you ever read more than a few sentences, Dano. The case of Warren and Marshall was a classic case where peer review blocked an outstanding paper because of entrenched beliefs. It is by no means unusual in the history of science for that to happen.

“The folk who do things for a living share their results in the journals. That’s the standard. That’s where people who do things for a living share their results. It’s too bad you don’t like their results.”

The folk who do things for a living quite often discuss their results in blogs like Real Climate. They also discuss the results of other papers. Steve’s results have been published in journals. He discusses them here. He also discusses the results of other papers. It’s too bad you don’t like his results.

I disagree. I think that the end run is not needed. If Steve writes up his stuff properly and submits to the appropriate journals, he can get it published.

TCO,

If it wasn’t clear, my post was not addressing where Steve is at this point in time. What you say may very well be true now, I am not so sure that it would still be true had not Steve and Ross defended their view via this blog.

“I’ve noticed something similar for Greenland – remind me to post this up.”

You stand reminded. Greenland is cutting edge stuff given the Kyoto Carbon Credit Casino forces now pushing it on the British Petroleum, ahem, BBC website. Big push in the
States too. Floating stories that the Greenland Ice Cap could collapse any day now without the fast institution of the Kyoto Protocols (which will do nothing to stop increased global carbon output but that’s just a pesky “fact”). It’s a media blitz push back to the debunking work of you and others. Now we get seeping melt water theoristics based on meta-research.

The Stalinistic rewriting of the MWP need no debunking, most everyone had schooling about that.

Rob,
Thanks for your civil and well though out posting. It was very refreshing. I do, however, have to respectively dissagree with you on at least one point.

It is no less respectable to replicate the results of a paper or falsify a theory than to propose theories and do the studies in an attempt to prove them. Science can’t operate properly without both. Falsifaction of theories does add to science because it clears away incorrect theories making way for new ones.

To this end it is critical that the data for all published studies also be published. It’s even more important when the studies are funded, even partially, but public money. Instead we have people like John Hunter telling us that he will only share his data with people that he considers “competent” to understand it, or more likely that will agree with his position. This is totally unacceptable. Science can only progress when the process is completely transparent.

There’s a tendency for impatience in getting “results” — just the trap dendrology has fallen into.

We’ve seen the considerable problems & uncertainties w/the current studies & methods. Overcoming these to achieve some credible GLOBAL temp reconstruction w/realistic error margains would be immense. It’d have to be done literally one site at a time, & somehow carefully assimulated. This would take years & require data transparency & cooperation between many researchers — obviously not the present situation. And consider that M&M are doing this on their own free time w/o pay or resources.